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Is the notion that species interactions are stronger and more specialized in the tropics a zombie idea? (guest post)

Note from Jeremy: This is a guest post by Angela Moles and Jeff Ollerton. A little while back I noted with interest that Angela had been publishing peer-reviewed papers arguing that some widely-believed generalizations about tropical ecology actually are zombie ideas. Jeff has been doing the same. I found their case convincing, but I’m not an expert on tropical ecology. So I invited Angela and Jeff to write a guest post making their case, in the hopes of sparking a productive debate on what I think is an important issue. Thanks very much to Angela and Jeff for taking the time to write what I think is both a provocative and well-argued piece, drawing on the work of others as well as their own work. Looking forward to a lively discussion in the comments.

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The concept of zombie ideas has been very useful in ecology. It turns out that there are quite a few venerable old ideas out there that should be dead because they have been slain by data and/or theory, but which still wander the world feasting on the brains of ecologists (such as common interpretations of the intermediate disturbance hypothesis; Fox 2013). In this post, we’re going to argue that the idea that species interactions are stronger and more specialized in the tropics is a zombie idea that needs to be slain.

The biotic interactions zombie started life as a perfectly good theory. The idea was that because the weather is always nice in the tropics, populations of plants and animals would not be knocked back by cold winters. The resulting population stability would allow plants and animals to reach high densities. In addition, lower rates of extinction coupled with higher rates of speciation mean that the greater species diversity with tropical communities results in species having to become specialized to exploit narrower niches, e.g. using a single food source. Year-round interactions with high densities of highly specialized attackers would naturally result in more intense (i.e. stronger) biotic interactions in tropical ecosystems, such as higher rates of herbivory and predation (Dobzhansky 1950; MacArthur 1972; Janzen 1973; Pennings & Silliman 2005). Furthermore the arms races resulting from these interactions would lead tropical species to be more heavily defended, and contribute to high diversity in the tropics (Coley & Kursar 2014).

The idea that biotic interactions are more intense and specialized at low latitudes is extremely widely accepted (e.g. Schemske et al. 2009; Coley & Kursar 2014). We both set out to study aspects of this idea with the full expectation that our work would confirm the traditional ideas. However, as the data rolled in, it became clear that many of the links in the lovely chain of logic above turn out to be weak or broken.

First, while the temperature is certainly stable and warm in the lowland tropics, many tropical areas experience substantial seasonality in precipitation (quantified in Vázquez & Stevens 2004). That is, despite all those postcards of sunny tropical islands, the weather isn’t always favourable for growth in the tropics (Figure 1). People who live in the tropics simply call their seasons things like “the dry season” and “the monsoon” rather than “summer” and “winter”, and are more likely to need a nice cold drink than a pair of skis.

Empirical data have also not supported the idea that population stability increases toward the tropics. Vázquez and Stevens (2004) compiled data for 12 major groups of mammals, birds and insects. Five taxa showed no relationship between population stability and latitude, 5 actually showed significantly greater stability at higher latitudes, and only 2 showed higher stability at lower latitudes. Meta-analysis showed that the overall effect of latitude on population stability was not significantly different to zero.

The evidence for greater specificity of interactions such as mutualisms, host-parasite and predator-prey relationships in the tropics is mixed, and certainly does not support the idea that the tropics are always more specialized (Ollerton 2012). Where the evidence is clear, such as for biotic pollination and frugivory, interactions are not more specialized in the tropics compared to extra-tropical regions once sampling effort is taken into account, suggesting that assemblages of interacting species in the tropics tend to be under-sampled (Ollerton & Cranmer 2002). More recently, an analysis of mutualistic interaction networks has shown that in the tropics, these networks tend to be LESS specialized (Schleuning et al. 2012). Finally, meta-analysis did not support the idea that species’ niche breadths are narrower at lower latitudes either (Vázquez & Stevens 2004).

Early reviews tended to support the traditional idea that biotic interactions were more intense in the tropics (Coley & Aide 1991; Coley & Barone 1996). However, these findings have been thrown in to doubt by a range of recent syntheses and meta-analyses. The empirical evidence has not supported the idea that terrestrial herbivory (Moles et al. 2011), marine herbivory (Poore et al. 2012), density dependent mortality in plants (Hille Ris Lambers, Clark & Beckage 2002) or seed predation (Moles & Westoby 2003) are stronger at lower latitudes.

In summary, the “strong and specialized biotic interactions in the tropics” hypothesis is dead. The quantitative evidence is counter to its predictions. Further, the chain of logic that led to its prediction of stronger biotic interactions in the tropics (including a stable climate, more stable populations, and more specialised interactions in the tropics) is in tatters. There is certainly scope for more studies on all of these topics, but at this stage it will take something quite substantial to overturn the mass of accumulated evidence against the idea that species interactions are always stronger and more specialized in the tropics. In fact, if there has been publication bias against results contrary to the traditional idea in the past (either through the file-drawer effect (Rosenthal 1979), or from reviewers being harsher on studies they perceived as getting the “wrong” answer), then the publication of syntheses and meta-analyses showing that the traditional ideas are not nearly as strongly supported as we thought (e.g. Vázquez & Stevens 2004; Moles et al. 2011; Ollerton 2012; Poore et al. 2012) might actually lead to a rapid accumulation of evidence contrary to the traditional ideas over the next few years.

Is the biotic interactions idea a zombie? Well, it certainly seems to be getting around a lot for a dead thing. Schemske et al. gave it a very warm review in a 2009 Annual Review of Ecology, Evolution and Systematics paper, and Coley and Kursar (2014) used it to underpin a recent perspective piece in Science.

Studies showing that species interactions are not stronger or more specialized in the tropics do not change the fact that tropical ecosystems are beautiful and amazing places. The observation that some aspects of ecology work in similar ways in tropical and temperate ecosystems is not actually all that surprising, and it means that tropical biologists and ecologists from other parts of the world can work together to advance our understanding of the ways that species interact. Finally, abandoning the idea that biotic interactions are more intense and more specialized in the tropics is like throwing away well-loved but worn out clothes: initially sad, but it will leave room in our collective wardrobe for a whole crop of exciting new ideas. Future progress will require researchers to more clearly define both their hypotheses (perhaps moving from conceptual to formal mathematical models) and their definitions: at least some of the disagreements in the literature stem from different definitions of terms such as “specialized” and “generalized” (Ollerton et al. 2007). This is clear when we consider that tropical communities, on average, certainly contain a higher number of functionally specialized pollination systems (e.g. bee, bird, beetle, fly, cockroach, etc.) and temperate systems have more plants that are functionally generalized (mixed bee/fly/butterfly, etc.) (Ollerton et al. 2006). However tropical plants are not more ecologically specialized, in terms of the number of pollinating animal species servicing each plant (Ollerton & Cranmer 2002). So, depending upon whether we are referring to functional or ecological specialization of plants in tropical communities, we could come to very different conclusions.

It is human to have trouble relinquishing ideas that we liked, and there’s no doubt that the latitudinal biotic interactions hypothesis was a really nice idea that made a lot of intuitive sense. Also, although it’s hard to test, we suspect that television documentaries that have traditionally focussed on highly specialised and intense interactions within the tropics have skewed our vision of what tropical ecology “should” be like, as opposed to what it’s really like, as has the tendency for ecologists to mentally compare tropical rainforests with temperate deciduous forests, ignoring all the other major vegetation types in each region. However, as scientists, we MUST disregard ideas once they have been disproved by data. As Neil DeGrasse Tyson says, “The good thing about science is that it’s true whether or not you believe in it.”

111 thoughts on “Is the notion that species interactions are stronger and more specialized in the tropics a zombie idea? (guest post)”

Wow – great piece! I think you have got it exactly right – there are a few specific ways in which interactions are stronger or different in the tropics, but not most of the general senses in which the world has been used. I do suspect this is an idea people will not want to let go of

Thanks Brian, glad you liked it 🙂 In retrospect something I wish we’d added to this piece is a comment about the difficultly of finding good data sets with which to test these ideas. Putting together data sets for species distributions over large geographical areas is hard enough, but good, large-scale data on species interactions is even more challenging.

Which provides one route to keep hanging on to these ideas, should one want to hang on to them–criticize the quality of the available data, perhaps except for a few studies that seem to show the expected latitudinal gradient.

The same strategy is one common way to defend the IDH. People complain that most field studies failed to find the predicted pattern because they must not have sampled a wide enough range of disturbance frequencies or intensities, for instance.

Yes, absolutely! So a good way to test these ideas in the future would be to focus on well-studied taxa (e.g. birds) which may have associated interaction data (e.g. parasites, feather lice, food types, predators) which have not been used previously to assess these kinds of questions.

While the general statement that species interactions are stronger in the tropics likely has little support, I believe the concept from which it is derived is slightly more complicated. Rather than being about absolute differences in the strength of interactions, my understanding is that it is about the relative influence of different factors on fitness. In the tropics, the hypothesis is that biotic interactions will have a greater effect on fitness than abiotic factors while the opposite should be true in temperate regions. None of the studies cited in this post compare relative effects of different factors. Further, I have yet to see a strong test of latitudinal differences in the strength of interspecific competition. Again, it is about the ability of individuals to acquire resources relative to all the other species that are trying to do the same. In temperate regions, the ability to acquire resources may be set more by actual resource availability and the traits that confer survival in physiologically stressful environments. IMHO, these ideas have not yet been “slain.”

Angela will probably have more to say about this once Eastern Australia wakes up 🙂 But I’d point out that the tropics can be physiologically stressful via a range of abiotic factors including drought, flooding, hurricanes, fire, high temperatures, low soil nutrient levels, etc. To paraphrase something John Harper once famously said: “Tropical rain forest is a stressful environment – for a penguin”.

But lowland tropics don’t freeze. Freezing kills cells, so organisms like penguins have to have adaptations to deal with freezing. Thus, there is a tradeoff for a Canadian tree between investing in freezing tolerance and investing in biotic interactions. That tradeoff does not exist for an Amazonian tree.

The nice thing about this hypothesis is that we can generalize to any abiotic stress other than freezing. Dessication kills cells too. I agree that it’s an over-generalization to say that all tropical ecosystems are abiotically benign. One could compare the relative contribution of biotic vs. abiotic factors to organisms’ fitness in wet vs. dry tropical forests. The idea is that, in a place that is abiotically stressful (dry forest), more of the variation in fitness in a population is due to abiotic factors. In a place that is not abiotically stressful (wet forest), more of the variation in fitness in a population is due to biotic factors.

Hi Carina – as I’m sure you realise, the point I was making about penguins in rainforest is that all environments are stressful to species that are not adapted to them. Amazonian trees have their own trade-offs: wet forest can be very “stressful” to a population if it’s seasonally flooded or if there are low levels of mineral nutrients in the soil or if they are being shaded by mature trees. I agree that there are testable hypotheses here but I don’t think that our starting point should be an a priori assumption that some tropical environments are less stressful than most temperate ones. I just don’t see that we have any evidence to support that.

With the massive recent interest in documenting thermal maxima and minima, it’s clear that many tropical animals are operating on the margins of their thermal constraints, within their given lineages. There are huge tradeoffs that Amazonian trees deal with to tolerate thermal conditions. The photo protective investments into xanthophylls might take a greater fraction of the tree’s budget than a Canadian tree might invest into freeze tolerance. Maybe, I don’t know. But it’s quite possible.

Yes, agreed that everything is adapted to some optimal range of temperatures and temperatures beyond that are stressful. But also, there are extreme temperatures–like freezing, which kills cells, or high heat, that denatures proteins–that I think we can agree are stressful to all life and require specialized adaptations to deal with. So I think we *can* have the a priori assumption that temperate places that freeze are more abiotically stressful than tropical places that don’t. All else being equal, temperate organisms have to invest in freezing tolerance, at the expense of *something else,* while tropical organisms don’t have to pay that expense. Ok, what does that mean? We really don’t know! We don’t know if that “something else” has anything to do with biotic interactions (herbivore defense? pollinator attraction?), because there’s no data on this, and tradeoffs are really hard to study. But it is a potential mechanism by which the abiotic environment, in this case freezing temperatures, can influence biotic interactions.

“All else being equal, temperate organisms have to invest in freezing tolerance, at the expense of *something else,* while tropical organisms don’t have to pay that expense.”

Hmm…This seems like a slightly different and broader use of the notion of “investment” than the ones with which I’m most familiar. Certainly there are allocation constraints–a unit of energy, materials, or time put to one use can’t also be put to a different use. So if, say, a plant builds a shoot, the required energy and materials can’t also be used to built roots. A mother who invests a lot of energy and materials into provisioning her offspring leaves less for herself and as a consequence may be at increased risk of dying from various causes.

But that allocation-based argument is narrower than just saying that “organisms that have to do *any* one thing *necessarily* will pay some cost in terms of their ability to do *some* other thing.” That very broad claim is false, I think. For instance, there are plenty of cases in evolutionary biology of positive pleiotropic effects–mutations arise that improve fitness under the conditions the organism is currently experiencing, and *also* improve fitness under other conditions, with no cost under any conditions. And we even have some theory about when we should expect to observe such positive pleiotropy (as opposed to antagonistic pleiotropy).

More specifically, with respect to freezing tolerance, it’s certainly the case that an organism that may encounter freezing temperatures needs *some way or other* to deal with that fact. And obviously organisms have evolved a huge range of ways to do that. But it’s not at all clear to me that all of those ways are well-described as arising from allocation constraints, or more broadly why we’d expect their evolution to necessarily have come at the cost of the organism’s ability to do something else.

I’m not so sure that the cost of freeze tolerance must necessarily be more costly than the cost of tolerance of abiotic conditions that occur in tropical nonfreezing areas. It depends on how you measure cost and constraints. Tropical organisms presumably have a larger energy budget than temperate ones (if they’re operating at an average higher metabolic rate), but a larger fraction of that budget might be allocated towards adapting to stressful abiotic conditions. Temperatures on the surface of the canopy can exceed 50C. Every sunny day. Imagine going from 50C to 15 C every day, compared to freezing for the winter. Which one is more costly? Hard to say, but it’s not safe to assume that the cost of freeze tolerance is greater.

This conversation isn’t going to go anywhere without data. Unfortunately, it doesn’t exist. Ideally, we’d want to know the proportion of variation in fitness (now AND in the past! we can get at past selection by looking at adaptive traits) due to biotic vs. abiotic selective agents at different latitudes, and by latitude I really mean temperature. Now that would be a big path analysis! We’d also like to know the magnitude of a tradeoff between adapting to these biotic and abiotic factors. Unfortunately, tradeoffs are really difficult to study.

So again…we need more data! Don’t give up on the question because the data aren’t there…yet.

Not sure where this comment will fill up in the thread, but it’s a penny comment only.

There are many obvious physiological functions subjected to tradeoffs that could quite exceed cost of investing in freezing resistance. Warm or dehydration kill cells too. There’s a high cost to heat tolerance in the tropics, and it’s not something you can switch off when climate is nice enough, like freeze resistance would usually happen to be. There’s a reason why adapting improved breeds to the tropics has never been as successful as thought at first: the temperate breeds usually don’t fit well and are not as productive as they should in the tropics. Part of the issue is heat resistance: they waste a lot of energy budget to cool down, and as a result, their theoretical productivity can be lower than local tropic breeds adapted to warmer climates, even if local breeds have not been improved for productivity the same way temperate breeds have been.

But I was rather willing to make a point from plants perspectives. In temperate climates, leaf expenditure is only supposed to produce leaves that last to the next freeze (at least in most species). You can spare the cost of producing leaves that are supposed to last much longer. When your leaves are best to keep working for undefinite time, you’d have to add the cost of making them more resistant to antagonists. I would tend to think this cost is much higher than freeze resistance (which evolved many times with independent solutions, even if the general path relies on anti-freeze properties of numerous cytoplasmic components). Secondary metabolites (usually involved in antagonist resistance) are heavily costly to produce.

Maybe there’s one way in which tropics would be more specialised than temperate climates: it would be plant investment in secondary metabolite chemistry. I don’t know if this subset-idea fits at all (because all plants worldwide produce SM compounds in a very diverse fashion) or if it is just still zombifying the twist. I’d think more at a total production level than overall compound diversification, but then we leave specialisation aside in a bad way… 🙂

Seedsaside – I decided not to go in to the secondary defence literature in this post to keep it simple, but we have looked at this – and it too failed to stand up to the data. My first approach was to visit 75 different ecosystems worldwide and quantify as many different types of defences as I could [Moles et al (2011) Putting plant resistance traits on the map: a test of the idea that plants are better defended at lower latitudes. New Phytologist 191: 777-788]. My second approach was to use meta-analysis to draw together the existing data from the literature (Moles et al 2011 Functional Ecology paper in the ref list above). The results were very similar in both analyses – the relationships are generally weak, but plants in the tropics are NOT more heavily defended (in the meta-analysis, chemical defences were significantly higher at higher latitudes, physical defences showed no relationship). Higher defences at high latitudes makes pretty good sense to me – consider a plant that lives in Greenland and only gets to have its leaves above the snow for a few weeks a year. This plant needs to do what it can to defend the precious leaves it has managed to grow – while in the more highly productive tropics, a plant can much more easily replace a lost leaf.

Incidentally, Carina, the idea that plants would have stronger anti-herbivore defences in the tropics was another of Schemske’s 39 points, so you see why I don’t consider everything on that list to be set in concrete (I should clarify here, I think most of Schemske’s work is fantastic, just not that AREES piece!).

Thanks Gunnar. As we say, it’s one measure of specialization; but the point we’re making is that there’s no consistency to the patterns we see: we don’t always find that tropical interactions are more specialized (or stronger) it depends on the taxa we study and the definitions that we use, and also on assumptions such as sampling effort.

Thank you for writing this piece; it is useful to think about what types of specialization (if any) may vary along latitudinal gradients.

I study tropical birds and wonder what your take is on latitudinal specialization (or lack thereof) in foraging behavior and diet in birds, which are commonly viewed to be more specialized in tropical than temperate zone birds. For example, there are several case examples suggestive of high dietary/foraging specialization in tropical birds, such as many species that exclusively forage on insects fleeing army ant swarms (a foraging behavior/diet with no temperate zone analogue).

Would you interpret these latitudinal differences in foraging behavior as examples of functional specialization rather than ecological specialization, as tropical species likely consume a similar number of insect species than Nearctic insectivorous birds? Actually, given the huge numbers of insect species in the tropics, tropical insectivorous birds probably eat a larger number of species, and, through that lens, could be viewed as less specialized than their temperate zone counterparts.

Or is specialization better indexed against available interactions, such as the proportion of available prey species consumed, in which case data might well show that tropical birds consume a smaller fraction of the insect species available at a given site than temperate birds do?

In either case, what is the nature of the data that would be necessary to rigorously evaluate specialization and move beyond qualitative story-telling?

I’m also interested in your comment about the mental comparison of humid tropical forests to temperate deciduous forests, which is the heuristic I am using above. Is it better to index specialization against specific climatic variables (temperature, seasonality etc) rather than raw latitude, in order to account for tropical arid regions, dry forests, savannas etc.

Thanks for the great questions Ben. To answer your first point I think I’d want to critically assess the diets of such bird species. Do they really only ever feed on insects that are fleeing ant swarms? Or is that just where we easily see them feeding? Having spent time looking at birds in tropical rainforest I know how difficult it is to observe them unless they are drawn to an abundant resource, e.g. insects fleeing ants! The rest of the time they may be feeding on less concentrated resources.

If it were demonstrated that their diets were so specialized, then yes, I’d describe it as functional specialization rather than ecological specialization, by analogy to the plant-pollinator example.

“Or is specialization better indexed against available interactions” – yes, that’s the best metric in theory, but how often do we know the number of potential species of prey/pollinators/herbivores/etc? It’s a hard one to quantify but perhaps points us towards the data we need, to answer your other question.

“Is it better to index specialization against specific climatic variables (temperature, seasonality etc) rather than raw latitude” – yes I should say so. In fact we’re moving in that direction already and have evidence that it’s past climatic stability, rather than latitude per se, which has more of an influence on specialization, at least in some types of interaction – see:

Thanks Ben – I do think remembering that the tropics isn’t all aseasonal rainforest, and that the temperate zone isn’t all deciduous forest is critical. I think replacing latitude with climate variables is a good thing to do – but even more important is to get more hollistic in our thinking about the world’s vegetation – the tropics include savanna, rainforest, and seasonally dry forests, and outside the tropics we have all sorts of things – including deciduous forest, grasslands (herbaceous taxa count too!), deserts, highly diverse shrublands (think S. Africa and Australia), rainforest (think New Zealand), coniferous forests, and tundra. I think we just fell in to comparing rainforest with the sort of deciduous forest found in N. America and Europe because that’s where most ecologists lived and worked.

I wholeheartedly agree and I think you’ve made a strong case here for abandoning the notion that interactions are stronger just because of richness or productivity or whatever else it is about the tropics that makes them different from the temperate zone.

I think so many of us are drawn to, and continually fascinated by, tropical biology because of the large number of easily observed and tightly coevolved mutualistic systems. That’s definitely true for ant people, who find the relationships like Acacia/Pseudomyrmex and Cecropia/Azteca to be compelling and memorable. I think the time spent looking at these very tight interactions spills over into generalizations about other interactions, which are not necessarily tight or specialized.

With the cumulative evidence of working with litter-dwelling ants over quite a while now, I don’t see any real evidence of tight species interactions among nearly all species. I imagine they’re about as familiar with one another as ships passing through the night, aside from worrying about the occasional pirate ship (army ants). I wouldn’t have imagined that starting out, and I thought competitive interactions were central to a lot of things. The evidence just doesn’t support it.

Thanks Terry. I think you hit the nail on the head, too much of a focus on particularly close interactions can spill over into general assumptions. Even on a moderate-sized island such as the UK I can point you to quite specialized interactions, but that doesn’t characterise all of our ecology.

I agree with Richard Feldman above, the hypothesis is more nuanced than as stated here. The hypothesis is better stated as, the relative contribution of biotic interactions to ***variation in organisms’ fitness*** is greater at lower latitudes. See Schemske et al. AREES 2009 paper p. 247 for a discussion of how we can conceptualize, quantify, and test this. This and other papers on the topic go on to explain how this could lead to greater speciation rates in the tropics, but that’s beyond the scope of this blog post.

I would argue that there really isn’t enough data on this topic to say whether or not it’s a zombie idea, which is why the AREES review doesn’t do a meta-analysis. When there isn’t even close to enough data for a meta-analysis, how can we say decisively whether there is support or not? Even in the first comment thread above, there’s a discussion about how difficult it is to test because there isn’t enough data!

What we do have is Table 1 in the AREES review: 30 out of 39 types of interactions show evidence of being stronger or more prevalent in the tropics (the other 9 showed no pattern). Not sure how one can argue that the data are overwhelmingly unsupportive, after seeing that table.

For example, your average temperate tree is wind-pollinated, wind-dispersed, and doesn’t have extrafloral nectaries. Your average tropical tree is animal-pollinated, animal-dispersed, and does. It’s a lot harder to say something about strength of ubiquitous interactions than prevalence of mutualisms, but I’d argue that that’s still an open question. One that I’m trying to address with my research.

Finally, I worry that the zombie label is thrown around too lightly. It’s so damn catchy, but is it always justified—especially in a case like this, where we badly need more data? As a young scientist, I read this with great trepidation. My dissertation is using novel empirical approaches to test parts (a) and (b) of the biotic interactions hypothesis. I would like to be a scientist at an R1 university someday, but in all likelihood more people will read this blog post than will ever read my empirical papers on this topic. So in a catchy headline and less than 1500 non-peer-reviewed words, I worry that my career is now going to be an uphill battle against the prejudice of people who, before reading this post, might have felt completely neutral about the question, but now would role their eyes and say, “That should have been dead long ago, this person is wasting their time testing it.” Isn’t that what calling something a zombie idea means? I sure hope that I don’t have a Dynamic Ecology reader on the hiring committee where I apply for jobs, because the last thing a young scientist needs is an eye roll when someone reads their CV.

Ok, zombie idea opinionating done. I’ll try and write a post on my own blog to expand and clarify the science a bit, like addressing the seasonality issue. I’ll post the link here if I do.

Oh, and by “parts (a) and (b)” I meant testing the hypothesis as stated in my first paragraph, and testing whether biotic vs. abiotic selective agents cause different rates of population divergence in allopatry. Originally I had elaborated more on other parts of the hypothesis but decided to save it for a longer post.

Carina, I would encourage you to keep doing what you are doing – questioning, digging deeper, pressing to have others back up their arguments – and not worry about if this post will cause some committee member to look down on your work, whose rigor will speak for itself. I think the best lesson to take from this is that we should always revisit truisms in light of new data. It may be that specialization is greater in the tropics, but only for certain interactions or in certain places. That’s worth knowing.

PS When ready, send your best stuff to us at Biotropica, ok? (Apologies to Dynamic Ecology for chumming for submissions on their blog)

I really hope that this hasn’t put you off testing these ideas, Carina, because (as you rightly say) we need more rigorous studies (though without unsupported assumptions as I mentioned above). Any committee worth its salt should appreciate what you’re doing, and you should be able to defend your position.

I’m going to leave Angela to comment more about the strength of biotic interactions hypothesis as that’s more her area, but I do note that we cite formal meta-analyses above, so clearly there’s enough data available to properly test some types of interaction.

One final point: I don’t know what the figure is for North America, but 60% of native tree species in the UK are insect pollinated, so assumptions about pollination systems of the “average” tree are incorrect! Yes there’s typically a higher proportion of plants that are animal pollinated in tropical communities compared to those at higher latitudes, but we have a paper currently in review showing that this is related to past climate (particularly rainfall) than to “tropicalness” per se.

Best of luck with your research and I look forward to reading your blog post.

For the pollination comment I was referring specifically to Regal 1982. He correlates the percent of wind-pollinated trees with latitude in the eastern US, and the 50% cutoff is around 34 degrees (about Tennessee). I guess since I live in Michigan, I was considering 40 degrees to be “average” 🙂 He says the percent of wind pollination is low, often zero, in tropical rainforests, but actual figures are difficult to obtain. Sounds like an update on the question is needed. It’s anecdotally interesting that it’s thought that most cases of wind-pollinated groups becoming secondarily animal-pollinated have occurred in tropical grasses and sedges (again, these are old citations and need updating). I came across one of these in Gamboa in Panama–really amazing to see grass flowers covered in bees!

@Carina re wind pollination – check out this recent paper of ours for a more up to date analysis of how the proportion of wind pollination changes with latitude (for all plants in a community, not just trees):

Tropical rainforests are under-sampled in this regard, but there’s usually a small proportion of wind pollination.

Yes, the sedges and grasses that have evolved animal pollination are really fascinating, but they are by no means restricted to tropical rainforest, or even the tropics. Peter Wragg and Steve Johnson have studied co-occurring species of Cyperaceae that are wind or animal pollinated in GRASSLANDS in South Africa! See:

I know transitions from wind to animal are not restricted to the tropics, I love Wragg’s work 🙂 A couple months ago I tried to look into how often animal pollination has been derived from wind pollination in tropical vs. temperate clades, but I gave up. Not enough information, as far as I could tell. There are some old, and as I said anecdotal statements that many genera that are temperate anemophiles are tropical entemophiles (Faegri and van der Pijl 1966), but I didn’t keep pursuing it to get the data myself. Would be a good project though…if you had good phylogenies. There’s the rub.

“So in a catchy headline and less than 1500 non-peer-reviewed words, I worry that my career is now going to be an uphill battle against the prejudice of people who, before reading this post, might have felt completely neutral about the question, but now would role their eyes and say, “That should have been dead long ago, this person is wasting their time testing it.” Isn’t that what calling something a zombie idea means? I sure hope that I don’t have a Dynamic Ecology reader on the hiring committee where I apply for jobs, because the last thing a young scientist needs is an eye roll when someone reads their CV.”

Carina, with respect, you’re *way* overrating the influence of this blog! I have yet to encounter or hear about *anyone* who takes what we write as gospel! (and believe me, there are times when I sure wish people would…) In all seriousness, you do *not* need to worry about whether or not someone will hire you, or roll their eyes about your research, based on what somebody has written on this blog. Yes, we’re widely read and discussed. But there’s a *big* difference between being widely read and discussed, and people just treating what we publish as gospel. Indeed, your own comments on this thread are part of what seems to me to be a very productive and high-level professional discussion, in which nobody (not even Jeff!) is unthinkingly taking the post as the gospel truth.

Further, Jeff and Angela’s post is a summary of their reading of the peer reviewed literature. I mean, they’ve got citations to a bunch of peer reviewed papers. If you disagree with their reading of the literature, fair enough–by all means explain why! But with respect, I don’t think it’s fair to just write this post off as not having been peer reviewed. The post cites the peer reviewed literature at length, so you can’t just wave it away as easily as that. Further, words mean what they mean, whether or not they’ve been peer reviewed. I’m sure that in your day-to-day life, you have lots of conversations with your adviser, committee members, and colleagues that you find really valuable. None of those conversations are peer reviewed. And I’m sure you’ve found it useful to attend conferences and give and listen to talks–none of which are peer reviewed. Think of this blog post the same way (I do). Rather than trying to just write this post off as not having been peer reviewed, why not just engage with it as you did in the first part of your comment? I’m sure that you have cogent reasons for disagreeing with the substance of the post–keep spelling them out! As a grad student working in this area, you absolutely have a lot you could add to this conversation, and I and the other commenters would *love* to hear what you have to say.

I think Carina is trying to engage with the post. The first half of her comment states her opinion and cites sources to back up her claims. Also, she states she’ll be commenting and writing more on her own blog and here.

Also, I did not get the impression that she just wrote the post off as “not peer reviewed,” but instead has legitimate concerns about how ideas, once labeled a “zombie hypothesis,” may be written off by readers of this blog if they don’t have specific expertise in the area. Yes, we expect everyone to think critically about every scientific idea they come across, but we all know that doesn’t happen. Trusted sources– like a conversation with a colleague or this blog– can influence opinion formation for those of us who, unfortunately, don’t have enough time to review the literature on the intermediate disturbance hypothesis or perform experiments on the species diversity gradient. And the term “zombie hypothesis” *does* suggest that the field is played out and the evidence/logic clearly points in one direction. In any case, I find it a valid point worth discussing.

It’s probably impossible to choose one’s style and rhetoric in a way that will please all readers. I know that the style of my own zombie ideas posts is quite attractive to many readers, while also turning some off.

Angela and Jeff can defend their own choice to use the term “zombie idea” in this particular case. I’ll merely suggest that, in general, I do think there are times and places in which it’s appropriate to use strong or attention-grabbing rhetoric in scientific communication. Those times and places may well be fairly rare, but I do think they exist:

But whether or not rhetoric is ever appropriate in scientific communication is something on which reasonable disagreement is possible, I think.

I’ll also suggest that one’s own reaction to rhetoric probably correlates with one’s reaction to the substance. If you agree with the substance, I think you’ll tend to like the rhetoric, or at least not mind it. If you disagree with the substance, you’ll tend to find the rhetoric off putting. I know that’s how it is for me sometimes, even when I make a conscious mental effort not to let that happen.

Re: mechanisms of opinion formation, sure. People obviously have to rely on trusted sources, take heuristic shortcuts, and come to opinions in all sorts of ways. I do that sort of thing just as much as anyone! But I confess I don’t see that that implies anything about the style in which blog posts should or shouldn’t be written, or that it implies anything about how strongly people should express their scientific views. Can you elaborate a bit, as I feel like I might be missing your point a little?

I’m not writing this off because it isn’t peer-reviewed; I’ve joined the fray. I just don’t think that a paper could get away with calling this idea dead.

It’s one thing to write a post about a disagreement with a hypothesis, and quite another to call it a zombie. That’s a powerful image, and having it associated with exactly what I’m studying is pretty terrifying. Compared to Monday, a smaller number of people in the world will think this is a question worth paying attention to (and funding…), when it’s been branded as the walking dead, as disproven, you can all go home now.

Don’t you think that someone who reads your blog might look somewhat askance at a job applicant who studies the IDH?

Don’t you want them to?

Is a zombie label justified here, or do we need more data? In a few years, I’ll have some nice data one way or another. For now, I think it’s still worth studying, not dead.

Thanks for continuing to engage with the post, apologies for misunderstanding the thrust of your comments about this blog post not being peer reviewed.

“Don’t you think that someone who reads your blog might look somewhat askance at a job applicant who studies the IDH?

Don’t you want them to?”

No, and no. Seriously. I’d echo the comments of several other folks–including Jeff Ollerton himself–regarding how science and scientists are evaluated.

As I said in reply to another commenter who is also uncomfortable with the “zombie ideas” rhetoric, I hear you and I think that’s something reasonable people can disagree on. What seems whimsical or funny or entertaining to some people is offputting to others. Rhetoric that merely gets the attention of some readers and gets them thinking, for other readers comes off as an attempt to browbeat them and discourage critical thought. And people who agree that idea X deserves to be called a zombie can disagree on whether idea Y deserves to be called a zombie. For instance, Markus has a very good comment in this thread suggesting that the problem with the ideas critiqued by the original post may not be that they’re zombies but rather that they’re vague. So Markus thinks the “zombie” label is out of place here–but if memory serves he thought the label was appropriate when I applied it to some versions of the IDH.

But I get the sense that we disagree not just about when “zombie ideas” rhetoric is appropriate, but also about its power to shape the views of readers. Personally, I don’t think calling something a “zombie idea” has much power, independent of the substantive evidence and arguments one musters. I think it mostly gets readers’ attention, but doesn’t do much to actually shape their views. Indeed, I think for many readers (maybe even including you?) this kind of rhetoric inspires skepticism and resistance rather than uncritical assent.

FWIW, a while back, I did a reader poll asking readers how my zombie ideas posts had affected their views on the IDH. The posts didn’t completely convince many people. But many readers reported that they were inspired to think harder about the IDH and question it.

FWIW, I think this is a great comment thread and I’d suggest that that’s in part because of, rather than despite, the way the original post was written.

The Schemske et al. AREES paper is not a quantitative review of the evidence, and I’d have to say that the citations in the paper seem a bit selective. I can’t tackle all 39 items on the list here – so I will just focus on the one that I have looked in to most comprehensively: terrestrial herbivory. While this is listed in Schemske’s table as something we are very sure about (ie, they are very sure that herbivory is more intense in the tropics), a review of the literature in 2011 (Moles et al – Functional Ecology – cited above) showed that only 37% of the 38 published studies quantifying herbivory across latitude actually showed the “expected” higher rates of herbivory in the tropics, and the average effect size in our meta-analysis was not significantly different from zero. That is, overall, the published data do not support the idea that herbivory is more intense in the tropics. Schemske et al are not the only ones selectively citing the literature – papers that show the “expected” higher level of herbivory in the tropics have been cited over 6 times more than papers that find the opposite http://library.queensu.ca/ojs/index.php/IEE/article/view/4490. In this case at least, the traditional idea that herbivory is more intense in the tropics is clearly not supported by a decent amount of empirical evidence – so the idea should be dead. Unfortunately, this particular idea is still widely believed (check out Coley and Kursar’s 2014 Science paper – in the reference list above) – so I’d say it most definitely qualifies as a zombie.

As for your study – I am delighted to hear that you are quantitatively testing some of these ideas – and I wouldn’t worry about the direction of your results one way or the other – if your study has an interesting hypothesis and a good design, there should be no problem at all in publishing it or getting the credit you deserve. Just don’t be too shocked if you get the opposite result to what you expected – as happened to both Jeff and I!

Re: the idea that the “biotic contribution” to variation in fitness is greater in the tropics, I’m not quite sure exactly what’s meant (can you provide links to a reference so I can brush up?) But it reminds me a bit of a common misunderstanding from my own field of population ecology. A common mistake in population ecology is to think that, if density-independent factors (e.g., weather variables) account for a large fraction of the observed temporal variation in per-capita demographic rates, that means that density dependence is weak or absent. In fact, that’s not just wrong, it’s the very *opposite* of correct. It’s only when density dependence is sufficiently *strong* that you expect density-independent factors to account for a large fraction of the observed temporal variation in demographic rates. I have an old post pointing this out (and it’s not me just asserting it–see the post for links to the peer-reviewed literature): https://dynamicecology.wordpress.com/2012/12/27/how-not-to-test-causality-observationally/

Do I have the wrong end of the stick here? Or is it possible that the same common misunderstanding from population ecology is also cropping up in tropical ecology? Honest question, I’m just trying to fit in what I’m reading in the comment thread here with material with which I’m more familiar…

I credit Brian McGill here for first introducing me to these concepts and the literature in which they were discussed.

My understanding is that the “biotic=tropical/abiotic=temperate” idea has its roots in Dobzhansky (1950) and MacArthur’s 1972 book, Geographical Ecology. Unfortunately, I do not own have access to MacArthur’s book at the moment. However, I have just re-read Dobzhansky’s article. It does mention many of the ideas discussed in this post.

First, the article is titled “Evolution in the tropics.” Hence, what Dobzhansky is trying to explain is how the main agents of selection differ in tropical and temperate environments. I guess this is what I meant too: what are the relative effects of biotic and abiotic factors on an individual’s fitness? Sure both can be strong, both can be weak, or only one is strong. What matters is whether, for an individual species, one is stronger than the other. And then, do we see generality in the relative strengths of biotic and abiotic factors for tropical vs temperate species.

And this is what.Dobzhansky has to say:
– “The process of adaptation for life in temperate and especially cold zones consists, for man as well as for other organisms, primarily in coping with the physical environment and in securing food. Not so in the tropics.” (p. 220).
– “Where physical conditions are easy, interrelationships between competing and symbiotic species become the paramount adaptive problem…This is probably the case in most tropical environments” (p. 220).
– “The role of the environment in evolution may best be described by stating that the environment provides “challenges” to which the organisms “respond” by adaptive changes…Tropical environments provide more evolutionary challenges than do the environments of temperate and cold lands. Furthermore the challenges of the latter arise largely from physical agencies…The challenges of tropical environments stem from the intricate mutual relationships among the inhabitants.” (p. 221).

Dobzhansky provides little data, only on the latitudinal diversity gradient. He reflects on chromosomal polymorphism among Drosophilia living in tropical and temperate environments, which he links to “adaptive versatility,” a term he uses to describe generalization. Interestingly, Dobzhansky acknowledges that specialization may not be greater in the tropics:
– “It might seem that…evolution in the tropics would tend toward perfection and specialization rather than to adaptive versatility. This is not the case, however.” (p. 217).
– “The widespread opinion that seasonal changes are absent in the tropics is a misapprehension.” (p. 217).

Hence, Dobzhansky makes no mention of whether interactions should be stronger or weaker in the tropics. Rather, he hypothesizes that interactions are more likely to be the primary selective force in the tropics and climate in temperate regions.

Re: relative strengths of selection arising from biotic vs. abiotic factors in different environments, I’m not a proper evolutionary biologist, but this seems to me to be a tricky thing to think about.

By “strength of selection”, we could mean the selection differential (covariance between phenotype and relative fitness), or the selection gradient (slope of the regression of relative fitness on phenotype) Either one will work for purposes of this comment (aside: As far as I know, these definitions are standard; I’m not trying to rig things by choosing to define “strength of selection” in some idiosyncratic way…).

It’s not necessarily the case that some factor that, say, produces high mortality will generate strong selection (whether defined in terms of selection differential or selection gradient). For instance, if because of high mortality (whether due to harsh winters or abundant voracious predators or intense competition or whatever) or whatever other reason everybody’s absolute fitness is fairly low, then there may well not much be much scope for variation in relative fitness. In that case, selection might be weak: the covariance between phenotype and relative fitness will be small, and the selection gradient will be flat. I say “might” because I’m just proposing a verbal argument here; you’d need a formal mathematical model to actually say anything with confidence (more on this below).

More broadly, it’s not necessarily the case that whatever factor has the biggest effect on absolute fitness has the biggest effect on the strength of selection.

I’ll also note that it’s very tricky to reason about the strength of selection without a formal mathematical model. It’s just tough for anyone to wrap their head around without the aid of math. Verbal arguments, no matter how plausible-seeming and no matter how smart the person proposing them, are likely to be incorrect.

For instance, my colleague Steve Vamosi has a nice little paper refuting a very plausible sounding verbal/graphical argument that selection on resource use traits should be maximized at intermediate resource levels: http://homepages.ucalgary.ca/~smvamosi/rundle_vamosi-ee_1996.pdf (I pick this example not because it’s relevant to the tropics per se, but just as one possible illustration among many of the general point).

Things get even trickier when you’re trying to reason about the relative strengths of selection that will be produced from two different selective agents. For instance, see this very nice study from Meyer and Kassen, showing that predation on bacteria reduces their abundances, weakening competition between them and so weakening diversifying (negatively frequency-dependent) selection arising from competition. But predation itself generates diversifying selection, so that in the presence of predators the bacteria exhibit more or less the same adaptive radiation that they exhibit in the absence of predators. I don’t mean that this example has any special relevance for the tropics, of course! It’s just the first example that occurred to me off the top of my head to illustrate the point that it’s really tricky to reason about the net effects of multiple simultaneous agents of selection.

Are there formal mathematical models in the literature of how the strength of selection arising from biotic vs. abiotic factors should vary between tropical vs. non-tropical habitats? If so, I’d be very interested to check them out. If not, I suggest that that would be a really useful thing for somebody to try to develop!

I think you are right, Jeremy. Certainly, if we are trying to test Dobzhansky’s original ideas then we need to address the issues you mention. Moreover, Dobzhansky presents a very loose and informal verbal-conceptual model littered with contradictions. We would definitely need something more rigorous if we wanted to really develop hypotheses.

I’m not sure how Dobzhansky’s ideas got mutated into the hypothesis that interactions should be stronger in the tropics. It would be interesting to see if, in the development of that hypothesis, researchers improperly cited him.

The paper that clarifies this best is Schemske, D. W. (2009). Biotic interactions and speciation in the tropics. Speciation and Patterns of Diversity. R. K. Butlin, J. R. Bridle and D. Schluter. Cambridge, United Kingdom, Cambridge University Press: 219-239.

Yeah, book chapter, sorry. Email me if you want a pdf (baskettc@msu.edu).

I think the more recent work on this question does a fine job of citing Dobzhansky. And Fischer; people put his 1960 paper in the “time and area” camp for latitudinal diversity gradient hypotheses, but he actually talks a lot about biotic interactions as well. I think recent work updates and clarifies their views without distorting them.

Fischer (1960) Evolution:
p. 197: “Since biotic diversity is the result of evolution, we may well ask whether differences in the manner of natural selection may partly account for biotas of different diversity.”
p. 198: “In the tropics, on the other hand, the physical environment is more benign to most organisms, and the highly selective interorganic struggle for existence is more apparent.”

I wonder how much of the confusion in all of this arises from miscommunication or misunderstanding between ecologists and evolutionary biologists? Seems to me that many of the proponents of this hypothesis are coming at it from an evolutionary angle (Wallace, Dobzhansky, Fischer, Schemske). Am I imagining that? Any ideas about what’s going on with that? Maybe we need a demographic model, but no one has tried yet.

Hey all, really nice post. I wonder, though, to what extent the dogma about specialization is actually dogma (or maybe a better question is ‘among whom’). Kricher’s Tropical Ecology textbook goes out of its way to point out that “it has long been assumed that specialization is widespread among tropical ecosystems, though that should not be taken to mean that all species have narrower foraging niches…specialization and narrow resource partitioning may not be the case for many, if not most species….” followed by examples (like Novotny et al. 2006) that blow away the specialization hypothesis, p. 139). I’m guessing most tropical ecology classes are taught that specialized mutualisms like figs-wasps Ants-acacias are exceptions. Rather, it seems like we’ve moved to pointing out that some things are more intense in the tropics (nest predation on birds, i think) and some actually shouldn’t be (like pollination).

The place where I’ve seen this idea persist most among tropical biologists is in plant-herbivore interactions and some types of predation (e.g., parasitoids). Vojtech’s work is really starting to eat away at the idea (pun intended); I think it’s now open season on the question of whether specialization in p-h interactions is rare, widespread, or common at some levels of organization (e.g., specialization in or on genera).

So I guess I’m asking – is it really as persistent an idea as you suggest it is? Or is it persisting among certain groups of ecologists?

Thanks for the great post – some good citations here to include in next semester’s class.

When we were trying to get the Ollerton & Cranmer (2002) paper published we met with a lot of resistance during peer review along the lines of: “why are you bothering to test this, we KNOW that tropical plants are more specialized and if your data say otherwise, then they are wrong”. Kudos to the editors at Oikos, they published it and I think their faith has been justified (115 citations and counting according to Google Scholar, which is not too shabby).

Over a decade later, I’m hearing more and more comments along the lines of “of course, we knew that tropical plants weren’t more specialized all along”, which seems revisionist to say the least!

As you point out there are certain topic areas where this “dogma” persists. But from personal experience I think that there’s also a geographical bias: quite a number of pollination ecologists who work only in the tropics think that their systems are more specialized. Likewise, pollination ecologists who only work in temperate areas often think that tropical plants are more specialized! Mobility between regions is breaking this down, and what I think we need is more interaction ecologists whose work spans a wide latitudinal range.

I don’t think it’s revisionist – I think it’s that as new data and analyses accumulate, people change their mind. It would be revisionist if people claimed they never believed the idea in the first place! But it seem like most people are willing to admit their ideas have evolved over time, no? At least I hope so.

Don’t get me wrong – I agree with your overall message that dogma needs to be questioned and that this particular dogma isn’t – in most cases – backed up by evidence. I’m just saying I’m not sure it’s actually “extremely widely accepted”. I think it’s accepted by the authors you cite (for whatever reason, including the fact that they work on systems where it might be true). But while I see lots of papers quantifying and testing mechanisms underlying specialization being submitted to Biotropica, I don’t recall many (any?) using the argument hat there is *more* specialization in the tropics.

“So I guess I’m asking – is it really as persistent an idea as you suggest it is?”

Interesting to hear this suggestion. Among the responses to my original zombie ideas post on the intermediate disturbance hypothesis was the claim that nobody actually believes the intermediate disturbance hypothesis anymore. But that’s not true. Citation data and the content of our textbooks shows that the ideas I criticized are alive and well among many ecologists: https://dynamicecology.wordpress.com/2012/04/16/yes-idh-zombies-are-still-worth-worrying-about/ So it’s intriguing to me to see the same suggestion raised here. But someone else will have to evaluate it, as I know little of the tropical ecology literature.

I think it’s useful to teach zombie ideas to show how the field has evolved, so seeing them in textbooks doesn’t bother me. But as you say in the post, it may not be clear in the book that they are in fact dead! Tropical ecology really only has one up-to-date textbook, and it does a good job with the topic of this post. In fact, while it mentions the idea that it is often thought tropical systems are highly specialized (and then explains that doesn’t seem to be true) I don’t think it says anywhere that it’s thought there is *more* specialized in the tropics. I’ll look more closely tomorrow to make sure.

I certainly think among macroecologists and people looking at the latitudinal gradient this idea is very much alive. Of course you would expect tropical field ecologists working on detailed systems like species interactions to be most up-to-date on what the data show, and those at more remove to be slower. Maybe this is the nature of zombie ideas – those close to the topic know better, but knowledge of the reversal either doesn’t get out or is slow to get out to the wider community?

“Maybe this is the nature of zombie ideas – those close to the topic know better, but knowledge of the reversal either doesn’t get out or is slow to get out to the wider community?”

I think there’s something to that. One fairly common reaction to my post on zombie ideas about the IDH was basically “Huh, I haven’t really thought about this stuff since taking my last undergraduate or graduate community ecology course, I hadn’t realized that the stuff I learned back then is now out of date.” I think that’s part of why it’s especially difficult to get rid of any idea that’s in widely-used undergraduate textbooks.

But I don’t think that’s all of it. My own experience is that “knowing better” sometimes consists of more than just “I work on this topic.” For instance, I don’t work on the IDH, or even on my preferred alternative (modern coexistence theory). But I was trained in a certain school of thought. That gives me a conceptual framework that helps me think through certain problems, and recognize certain sorts of mistakes whenever they happen to crop up.

And we can probably all also name people (in and outside of science) who continue to stick with some idea come hell or high water precisely because they work on it, so that they’re highly invested and reluctant to give it up.

Great post and many good points.
I appreciate the zombie idea: it adds wit and humour. But, as several post above note, we need to be careful about the all-or nothing opinion swings that seems to come with such labels (just what has and what has not been shown to be incorrect). Realities are often much more nuanced leaving considerable scope for disagreement and uncertainty.
To mix some metaphors: Where Jeremy sees an IDH zombie is his bathtub I also see a perfectly healthy baby lying next to it in the bathwater. That was what motivated David and me to respond in TREE and previous guest blog see https://dynamicecology.wordpress.com/2013/09/03/a-thumbs-up-for-the-intermediate-disturbance-hypothesis-guest-post/.
But again — great post here!

I’ve been staying out of this debate up to now because I’m not convinced that a clear-cut answer is possible yet. As someone who (a) has worked on plant-insect interactions, (b) has just written a chapter on the latitudinal diversity gradient, and (c) has a wide geographical range to my research interests, I should be qualified to jump one way or the other, but it doesn’t appear to me that a binary decision is possible, which makes me wary of crying zombie.

The two strands to both the original post and subsequent discussion highlight distinct questions. The first is whether interactions in the tropics are more specialised. Emilio Bruna points out Vojtech Novotny’s 2006 work suggesting that plant-herbivore relationships are not. The following year Nature published a comparable study by Lee Dyer suggesting that they are. I saw them both speak in the same ATBC session in 2007, and I don’t think anyone walked out convinced that one was right and the other wrong, more that we still had plenty to think about. Undersampling in the tropics, combined with considerable uncertainty about the presence of cryptic species (e.g. Smith, Rodriguez et al. 2008, PNAS), means I’m content to hedge my bets for the time being.

Secondly, are biotic interactions more important in the tropics? The chief weakness with this question, as others have pointed out, is that it is imprecise in formulation and it’s uncertain how any effective comparisons can be made. Are we talking about impacts on population dynamics, recruitment success, range sizes or some other metric? Will all these behave in the same way?That no agreement has come about is perhaps another case of an apparently intuitive and qualitative statement by Dobzhansky, Hamilton and others turning out to be fiendishly difficult to validate empirically.

In short, I don’t consider it a zombie idea, nor (as Carina fears) a zombie research area. Instead, it’s an area where we need to step back and concede that simplistic expectations have failed, and we need to consider the theoretical underpinnings carefully before reentering the fray. I hope to see lots more papers on it in the future and — Carina — you can rest assured that plenty of us will be reading them.

Markus, spot on – the imprecise formulation of the question and metrics by which it is measured is the problem, rather than the idea itself. That’s only one reason why Lee and Vojtech could both be right.

I think the same thinking applies to the IDH stuff. The debate is not about the original idea but rather the way teh IDH label has subsequently been described, applied and generalized.
Seems these zombies evaporate when we shine enough bright light on them.

Nice comment! We should be in touch, sounds like we have similar research interests. I agree, these ideas are really difficult to test! This will be my first summer doing lots of data collection, it’s taken me two field seasons just to find and develop systems.

I’ve got to partly disagree, Markus, I think that there’s a clear cut answer to the (simplistic) question: “Are tropical interactions, on average, always more ecologically specialized and stronger than temperate interactions” and the answer has got to be “no”. That’s what I see as the zombie idea we’re that addressing here.

Now there may well be examples where a particular class of interaction is stronger/more specialized in the tropics, for example Dyer et al. (2007) as you point out had such evidence for Lepidoptera host specificity (though if I recall their data set actually resolves to only a handful of sites in the New World). But it’s certainly not true of all interactions all, or even most, of the time.

It this encourages people to start looking at these questions more critically, then we’ve done our job.

But any idea phrased by words like “all” or “always” is likely a “zombie” idea. Exceptions abound. I don’t know any ecologist that would dispute that. Of course, trying to define when the exceptions make the rule or when we can call a phenomenon general despite the exceptions is, perhaps, a subjective endeavour.

I agree with Richard on this one. We can certainly reduce many sources of subjectivity, but likely not all and not entirely (e.g. how study cases were originally selected from the universe of possible options is seldom clear).

I think most of this confusion on the latitudinal gradients of specialization arises from the concept itself. In different papers people use different theoretical concepts of specialization created at different levels of ecological complexity (from the individual to the community), and asses them through a variety of proxies. Nevertheless, in the end we try to discuss all this diversity of ideas as if we were talking about the same thing. The first step towards disentangling this web of theory and evidence is to clarify the terms and proxies.

Thanks for this great post, Jeff and Angela! You are making some good points here – but I agree with others above that it’s not appropriate to call this one a zombie. Besides just a being an attractive and provoking term, I believe the zombie label does influence people’s opinion, even though when asked specifically one might have a more nuanced opinion. And an important difference to the IDH zombie is that here it is not about an idea that doesn’t make sense but about a belief about how the world looks like not supported by sufficient data. The problem here is that many people not looking at the details assume biotic interactions in the tropics are stronger and more specialized (at least it’s what most people first expect when I talk to them). Do unsupported popular assumptions qualify for the zombie label?

I totally agree that there is not enough evidence to support the latitude-specialization assumption (I cannot really speak about interaction strength). Current evidence suggests that there is no strong general pattern – but which “general patterns” in ecology are actually general? Sometimes, knowledge of an average trend may be useful despite it having many exceptions. The general pattern makes it easy to speak about it in simple words and it can be remembered by people working on other topics. But granted, on this topic people should indeed better remember “there is no general pattern”, while people working on the topic should rephrase the questions.

And then there was the point that we need more data for solid answers in this area. That is so true! However, I think we also need to deal better with the data we have (and those yet to gather). Besides the important differences in specialization concepts mentioned by Jeff, Marco and others, sampling effects are particularly challenging when we compare samples of different diversity. However, people often only consider sampling effects in the most obvious cases. For example, the Dyer et al. 2007 paper (cited above) suggests that higher turnover between host plants in the tropics is a robust additional confirmation of higher specialization in the tropics, but it is exactly what can be expected for a community with higher diversity. We need to develop (or just apply?) better methods.

Understanding the variation of biotic interactions is important. Latitude is probably not the most important predictor. People should refrain from using the assumption of high tropical specialization to build other theories on it. But the question, stated broadly (“how do interactions vary from tropics to high latitudes?” rather than “are the tropics more specialized?”), is far from being a zombie – not to be abandoned, but to receive more collaborative effort!

Nice comment Jochen – thanks. I think if an idea has been proven to be wrong (by data and or theory), then it is scientifically dead. If people are still treating it as though it hasn’t been disproven, then you have a zombie idea. However, I think you raise an important point – we do need another term in ecology – for ideas that have always been assumed to be true but which have never been appropriately tested. There are loads of these in ecology (and I suspect there are in all fields) – particularly from the 60s and 70s when there were a lot of nice ideas papers coming out but the amount of data available was tiny compared to what we have now, and the computing power and stats weren’t really up to properly testing complex ideas anyway. I put this out on facebook a couple of weeks ago and the best candidate name for these “always assumed to be true” ideas so far is “Sheep ideas”, but that’s not nearly as catchy as zombie ideas, so I’d love to hear any other suggestions!

I kind of like “lemming ideas” – even though the image is not biologically correct (indeed depends on a Disney movie which behind the scenes was mechanically launching lemmings off a cliff) the popular culture idea of walking off the cliff into thin air by the thousands seems to me related to the notion of embracing an idea that has no empirical support.

I love both “sheep ideas” and “lemming ideas”, but here’s my question: are people who believe in these ideas going to be any happier than if you’d called them “zombie ideas”? Honest (and semi-serious) question.

I guess what I’m really asking is: is there any label or meme that one can use to humorously call attention to the need to seriously question some idea, *without* it coming off as threatening, overstated, or off-putting to those who believe in the idea? I’m thinking not…

So if we’re going to go with “sheep ideas” or “lemming ideas”, what sort of joke photos would I have to post, instead of ones like this and this? 🙂

@Jeremy – nope people won’t like being told that their pet idea is a sheep or lemming idea either. But scientists would all be better off if we had a little sense of humor about ourselves 🙂

And Angela is right – a sheep/lemming idea is different than a zombie idea. It needs a new name not because it won’t offend people (it still will). It needs a new name because it is a different concept. Killed and should be in the grave is different than thousands of people embracing without a shred of evidence.

I agree that whatever words you use, some people will be offended (particularly since several of our really venerable old and well-trusted ideas fall in the “not properly tested yet” basket when you look closely) – but I actually think that’s ok – half the point here is to draw attention to the existence of these untested yet universally assumed to be true ideas. Like sheep, these ideas seem to be everywhere (I grew up in New Zealand, where sheep outnumber people 7:1).

Oh, and you definitely shoudn’t replace the zombie merchandise (which I didn’t know about before – brilliant) – this is a different concept and they should coexist just fine – just add a lemming/sheep line.

Sure “zombie”, “sheep,” and “lemming” are catchy and catchy is important for communication. However, don’t we already have the continuum of hypothesis-rule-law? The problems we are discussing occur when some treat a hypothesis as if it were a rule or law. Alternatively, we can just call an idea “data deficient,” which seems fairly innocuous to me.

And just for entertainment, here’s the video for lemmings: https://www.youtube.com/watch?v=AOOs8MaR1YM
(complete with music and utter nonsense announcer voice over – recall Disney was actually launching these poor guys off a spinning turntable – something they couldn’t get away with today). I actually remember being shown this moving in like 3rd grade.

We’re running up against nesting limits in a bunch of subthreads, so I’m starting a new subthread.

In a weird way, I’m actually slightly disappointed by the thoughtful, informed, nuanced discussion. Because anecdotal evidence suggests that there are some people working on these topics who really do believe wholeheartedly and unreservedly in zombie versions of these ideas. To the point where they recommend rejection of any empirical paper that doesn’t find the patterns that we “know” exist, because any such paper “must” be fatally flawed:

“But any idea phrased by words like “all” or “always” is likely a “zombie” idea. Exceptions abound. I don’t know any ecologist that would dispute that.”

Yes, absolutely, I completely agree! But as Jeremy notes above, there’s anecdotal evidence that there are some ecologists who believe it, even if they’re not defending it. In that sense, the more nuanced ecologists are not the right audience for a post such as this.

“Of course, trying to define when the exceptions make the rule or when we can call a phenomenon general despite the exceptions is, perhaps, a subjective endeavour”

That’s true, but when the weight of evidence is against a proposition, something has to give.

@ Richard & Jeremy – in this case it’s not just that there’s a deficiency of data, it’s that someone can pick and choose studies that support their pet hypothesis, and cite those at the exclusion of the others.

Yes, agreed. I took Richard’s remark to be a general one, about the sort of innocuous term one might use to describe any situation in which data are lacking or inconclusive (perhaps despite many people thinking otherwise). But in this particular situation, I agree with you: we now have a lot of data on various common formulations of the idea that species interactions are stronger or more specialized in the tropics. Those common formulations have been found wanting. Whether quite different formulations of the same broad ideas might be true is an open question, it seems.

Another general remark: I have somewhat mixed feelings about calls for “more data” and “better developed/more precise/more nuanced hypotheses” in these sorts of situations. I was going to comment but found the comment was turning into a post, so I’ll probably do a post at some point.

Re your general remark: just to make my view on this clearer – I didn’t mean just to rephrase the question to get better testable hypotheses with the same interpretation. We have to get over this meme – but we have to keep working on the subject, which is (global) variation of biotic interactions. And this requires more data (or sharing of old data) and may contain some of the old ideas if they are not over-generalized.

Yes, exactly. That’s the sort of thing I plan to talk about in my future post–the various things one might mean when one says “we need more data” or “we need better developed hypotheses” or “we need to keep pursuing this topic”. Sometimes such calls are very welcome–and sometimes they’re just a way to try to defend zombie ideas and dead end lines of research. It all depends on exactly what sort of new data are being called for (more of the same sort we’ve been collecting, or a different sort, or what?). What sort of hypothesis development is being called for (just rephrasing the question slightly, or deriving a formal mathematical model, or what?). Etc.

Basically, I want to talk about the kinds of traps one can fall into when one’s initial idea doesn’t seem to be working out or needs to be further developed. Still making notes and mulling over ideas, suggestions welcome!

Great post (I recommend to others). Well done for pushing back.
Like you I am pleased to see the discussion but find the “zombie” label somewhat irritating when I disagree with the diagnosis! We need more nuance.

I only just became aware of this post: what a great discussion!! I really enjoyed it, more for the fabric of scientific discourse than for the latitudinal gradient, to which I am now even more comfortably agnostic. I do feel the concerns brought forward by Corina, where she is worried about undermining her research topic. I have had this actual experience in a grant application, where the hypothesis I wanted to test was “falsified” in a high impact paper published after I submitted my proposal, and which was stated as 1 of 3 reasons why my proposal didn’t get funded. This was maddening and wrong (actually I published a sort of rebuttal of that paper of which the grant reviewers were unaware, and in any case, the hypothesis was sufficiently broad to not be dismissed by a single high-impact paper) , but I certainly don’t blame the authors of that paper: it is the grant-reviewers (and by extension Corina’s selection panel) who are wrong! The take I get from this discussion is that the idea is actually much more alive than when people just take it for granted (and think it is long settled), which should give more impetus to studies addressing it, independent of the outcome. I don’t think this is an idealization, but how many of us work (except for the most lazy reviewers, which I hope are few).

Hi Erik – thanks for your comment, glad you enjoyed the post and the discussion. You make an interesting point here which I think supports something Jeremy (?) said earlier, that the perception of an idea/hypothesis by (often) non-specialists can be affected by all sorts of things, and using the label “zombie” is just one of them. That’s something which all academics have to deal with all of the time. One of my Brazilian collaborators, who has just completed his PhD, told me that when he first began his research a few years ago he was advised by one of the senior academics in zoology to give up pollination biology because “it’s all been discovered, there’s no more interesting questions”! Lazy ignorance may be more common than you think 🙂

Looking at your research interests, mycorrhizal relationships are an area that could really contribute to testing hypotheses about latitudinal trends in interactions as it’s clear that these are incredibly important in temperate terrestrial ecosystems: but are they “more” important in the tropics? A specialist with a good knowledge of the literature could produce an interesting meta-analysis I think.

I think that would definitely be an interesting topic. However, defining importance is going to be very hard, like in any other research topic in this post :-). Regarding a comparison between forests, the shift from AMF to generally EcM fungi with increasing latitude might also complicate comparisons. But still worth a try!

Bumping an old thread here, but I think it’s worth it. I just came across this 2014 paper in a rather obscure journal (Austral Entomology) which gives a nice summary of the problems surrounding estimates of plant-herbivore specialisation and where evidence is lacking. It reads like the introduction to a grant proposal, which it probably is, but none the worse for it.http://onlinelibrary.wiley.com/doi/10.1111/aen.12111/abstract

Thanks Carina, I had seen the paper. At the risk of re-opening the debate, I think that it’s more accurate to say that the paper finds “greater herbivore specialization at lower latitudes” for some (but not all) guilds (see their Fig. 3 and p.444) in a data-set heavily biased towards the New World, with no representation from tropical (or temperate) Africa or tropical Asia.

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